Download On universal common ancestry, sequence similarity

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RESEARCH
Open Access
On universal common ancestry, sequence
similarity, and phylogenetic structure: the sins of
P-values and the virtues of Bayesian evidence
Douglas L Theobald
Abstract
Background: The universal common ancestry (UCA) of all known life is a fundamental component of modern
evolutionary theory, supported by a wide range of qualitative molecular evidence. Nevertheless, recently both the
status and nature of UCA has been questioned. In earlier work I presented a formal, quantitative test of UCA in
which model selection criteria overwhelmingly choose common ancestry over independent ancestry, based on a
dataset of universally conserved proteins. These model-based tests are founded in likelihoodist and Bayesian
probability theory, in opposition to classical frequentist null hypothesis tests such as Karlin-Altschul E-values for
sequence similarity. In a recent comment, Koonin and Wolf (K&W) claim that the model preference for UCA is “a
trivial consequence of significant sequence similarity”. They support this claim with a computational simulation,
derived from universally conserved proteins, which produces similar sequences lacking phylogenetic structure. The
model selection tests prefer common ancestry for this artificial data set.
Results: For the real universal protein sequences, hierarchical phylogenetic structure (induced by genealogical
history) is the overriding reason for why the tests choose UCA; sequence similarity is a relatively minor factor. First,
for cases of conflicting phylogenetic structure, the tests choose independent ancestry even with highly similar
sequences. Second, certain models, like star trees and K&W’s profile model (corresponding to their simulation),
readily explain sequence similarity yet lack phylogenetic structure. However, these are extremely poor models for
the real proteins, even worse than independent ancestry models, though they explain K&W’s artificial data well.
Finally, K&W’s simulation is an implementation of a well-known phylogenetic model, and it produces sequences
that mimic homologous proteins. Therefore the model selection tests work appropriately with the artificial data.
Conclusions: For K&W’s artificial protein data, sequence similarity is the predominant factor influencing the
preference for common ancestry. In contrast, for the real proteins, model selection tests show that phylogenetic
structure is much more important than sequence similarity. Hence, the model selection tests demonstrate that real
universally conserved proteins are homologous, a conclusion based primarily on the specific nested patterns of
correlations induced in genetically related protein sequences.
Reviewers: This article was reviewed by Rob Knight, Robert Beiko (nominated by Peter Gogarten), and Michael
Gilchrist.
Background
In a recent study, I applied model selection theory to a
data set of universally conserved protein sequences, in
an attempt to formally quantify the phylogenetic evidence for and against the theory of universal common
ancestry (UCA) [1]. For the conserved protein data, this
Correspondence: [email protected]
Biochemistry Department, Brandeis University, Waltham, MA 02454, USA
study demonstrated that UCA is a much more probable
model than competing independent ancestry models.
One of the notable strengths of this study is that it provides evidence for common ancestry without recourse to
the common assumption that a high degree of sequence
similarity necessarily implies homology.
This UCA study was subsequently criticized in a paper
by Koonin and Wolf (hereafter referred to as K&W), in
which they argue that the results in favour of UCA are
© 2011 Theobald; licensee BioMed Central Ltd. This is an Open Access article distributed under the terms of the Creative Commons
Attribution License (http://creativecommons.org/licenses/by/2.0), which permits unrestricted use, distribution, and reproduction in
any medium, provided the original work is properly cited.
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“a trivial consequence of significant sequence similarity
between the analyzed proteins” and that my tests “yield
results ‘in support of common ancestry’ for any sufficiently similar sequences” [2]. Here I show that K&W’s
conclusions are incorrect. While sequence similarity is a
highly probable consequence of common ancestry, similarity alone is insufficient to establish homology by the
model selection tests. Rather, the phylogenetic pattern
of nested, hierarchical, sequence correlations is the
dominant factor that forces the conclusion of common
ancestry for the real protein data. Before considering
K&W’s specific arguments in detail, I give an extended
background to the question of universal common ancestry and provide a setting for understanding why null
hypothesis tests of significance, such as BLAST-style Evalues, are inadequate to quantitatively address the evidence for and against UCA.
Universal common ancestry: The qualitative evidence and
need for a formal test
Universal common ancestry is the hypothesis that all
extant terrestrial life shares a common genetic heritage.
The classic arguments for common ancestry include
many independent, converging lines of evidence from
various fields, including biogeography, palaeontology,
comparative morphology, developmental biology, and
molecular biology [1,3-14]. The great majority of this
evidence, however, is qualitative in nature and only
directly addresses the relationships of limited sets of
higher taxa, such as the common ancestry of metazoans
or the common ancestry of plants.
The broader question of universal common ancestry is
much more ambitious and correspondingly difficult to
assess. Are Europeans, Euryarchaeota, Euglena, Yersinia,
yew, and yeast all genetically related? Of course, biologists routinely incorporate all of these taxa into a universal phylogenetic tree, which is an explicit
representation of the genealogical relationships among
these diverse taxa. But any group of taxa can be connected in a tree; one can even make a phylogenetic tree
from random sequences or characters. Yet is a tree itself
justifiable in light of the evidence? In a paper that motivated my original test of common ancestry, Sober and
Steel set out the issue very clearly [11]:
When biologists attempt to reconstruct the phylogenetic relationships that link a set of species, they
usually assume that the taxa under study are genealogically related. Whether one uses cladistic parsimony, distance measures, or maximum likelihood
methods, the typical question is which tree is the
best one, not whether there is a tree in the first
place.
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This is the question I set out to answer: Is there a universal tree — or, more broadly, a universal pattern of
genetic relatedness — in the first place?
Several researchers have recently questioned the nature and status of the theory of UCA or have emphasized
the difficulties in testing a theory of such broad scope
[11,15-18]. For example, Ford Doolittle has disputed
whether objective evidence for UCA, as described by a
universal tree, is possible even in principle:
Indeed, one is hard pressed to find some theory-free
body of evidence that such a single universal pattern
relating all life forms exists independently of our
habit of thinking that it should [19].
This sentiment was echoed also by K&W, who concluded that a “formal demonstration of UCA … remains
elusive and might not be feasible in principle.” [2]. Such
criticisms of UCA point to a need for a formal test,
similar to the formal tests of fundamental physical theories like general relativity and quantum mechanics.
Darwin originally proposed UCA in 1859, yet was
characteristically circumspect, only committing to the
view that “animals are descended from at most only
four or five progenitors, and plants from an equal or lesser number” [3]. The hypothesis of UCA was evidently
an open question at least until the mid 1960’s, when a
debate about UCA and the universality of the genetic
code (then as yet undeciphered) played out in the pages
of Science. One of the most celebrated arguments for
UCA is based on the fact that the genetic code is identical, or nearly so, in all known life. The argument had
been circling informally for some years before Hinegardner and Engelberg first presented it in detail [20-23]:
Because the genetic code should remain invariant, its
constancy can be used to establish the number of
primordial ancestors from which all (present) organisms are derived. If, for example, the code is universal … then all existing organisms would be
descendants of a single organism or species. If the
code is not universal, the number of different codes
should represent the number of different primordial
ancestors …
Hinegardner and Engelberg’s reasoning hinges on the
assumption that the genetic code is so important for
fundamental genetic processes that any mutations in the
code would be lethal. Carl Woese criticized this argument, noting its dependence on the assumption that the
genetic code is a “historical accident” and must not be
“chemically determined” [23]. Woese was a proponent
of the “stereochemical hypothesis”, which holds that the
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association between a certain codon and its respective
amino acid is dictated by chemical phenomena — that
is, the observed code is required somehow by the laws
of physics, perhaps by binding affinity of the nucleic
acid codon to its corresponding amino acid [23-26].
Woese was also sceptical that the code was “frozen”,
and he postulated plausible mechanisms by which a
degenerate code could evolve. If the code were somehow
determined by physicochemical principles and evolvable,
then multiple origins of life could conceivably converge
independently on the same code. However, the stereochemical hypothesis was considered and largely disregarded by most researchers, including Francis Crick, due
to a lack of evidence and difficulty in imagining a possible mechanism [20-22,24].
In 1968, Crick still presented the “frozen accident”
argument for UCA with some reservation [24]. But by
1973, in his famous essay on the explanatory power of
evolutionary theory, Theodosius Dobzhansky laid out
the existing evidence for UCA as if it were beyond dispute [4]. According to Dobzhansky, the primary support
for UCA is given by several key molecular similarities
shared by all known life: (1) the “universal” genetic
code, (2) nucleic acid as the genetic material, (3) shared
polymers such as proteins, RNAs, lipids, and carbohydrates, and (4) core metabolism. These are today still
the main arguments for UCA.
The standard presentation of this evidence is, however, strictly qualitative; it does not quantitatively assess
the likelihood that these commonalities could be arrived
at independently from multiple origins. Each of Dobzhansky’s arguments for UCA has its weaknesses, and
Sober and Steel provide several criticisms of these standard arguments [11]. While a detailed analysis of these
lines of evidence for UCA is beyond the scope of this
article, as a case study let us briefly revisit the “universal” genetic code, widely considered the most persuasive
evidence for UCA [5,6,10,24].
The origin and evolution of the genetic code is still an
open question [25,27], yet recently a modification of the
stereochemical theory has made a comeback, in the
form of the “escaped triplet hypothesis” of Yarus and
Knight [28,29]. Their hypothesis has the great advantage
that it is based on a large body of experimental data
that has shown a significant chemical association
between amino acids and their corresponding codon/
anti-codon triplets found in RNA aptamers.
From Yarus and Knight’s work, we now have empirical
support for an association of specific codons with their
respective amino acids, which means we have a viable
mechanism for evolving similar or identical genetic
codes from independent origins. Hence, the plausibility
of a stereochemical theory decreases the force of the
“frozen accident” argument for UCA — but by how
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much is unclear. Furthermore, we also know now that
the genetic code is far from “frozen”, and that it continues to evolve [27].
Ideally, we would like to evaluate the evidence for
UCA from the universal genetic code, accounting for
the frozen accident and stereochemical hypotheses and
allowing for code evolution. For instance, we could calculate the following two different probabilities, and
compare them: (1) the probability of arriving at a near
universal genetic code assuming two or more independent origins and convergence due to chemical constraints from the escaped triplet hypothesis, versus (2)
the probability of arriving at a near universal code
assuming a single origin and a “frozen accident”. Of
course, reasonable and persuasive verbal arguments can
be made on this point [25], and the qualitative evidence
compellingly supports universal ancestry. But quantitatively estimating these probabilities is non-trivial. To
calculate these probabilities we need formally specified
stochastic models for how genetic codes evolve under
both hypotheses — namely, we need well-defined likelihood functions, probability distributions for the
observed data given each of the competing hypotheses.
We currently have no such formal models for genetic
code evolution [11,12,25,27]. The calculations are
further complicated by the fact that there are other
plausible hypotheses for the evolution of the code with
empirical support [25,30], not all of which are mutually
exclusive. Consequently, it is currently impractical to
construct a formal, quantitative test of UCA using evidence from the genetic code.
Fortunately, however, we do in fact have ready-to-use,
well defined, and widely accepted stochastic models for
the evolution of protein sequences. These phylogenetic
models of sequence evolution have been developed in
detail over the past few decades in the field of molecular
evolution, and they benefit from both a firm theoretical
basis and widespread empirical support from genetics
[31]. It is for these very reasons that I based my formal
probabilistic, model-based tests of UCA on protein
sequence data.
Sequence similarity and homology are not equivalent
One common thread among the various arguments for
common ancestry is the inference from certain biological similarities to homology. However, with apologies to
Fisher, similarity is not homology. It is widely assumed
that strong sequence similarity indicates genetic kinship.
Nonetheless, as I and many others have argued
[1,32-40], sequence similarity is strictly an empirical
observation; homology, on the other hand, is a hypothesis intended to explain the similarity. Common ancestry is only one possible mechanism that results in
similarity between sequences. In a landmark paper on
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the inference of homology from sequence similarity [33],
the late Walter Fitch presented the problem as follows:
Now two proteins may appear similar because they
descend with divergence from a common ancestral
gene (i.e., are homologous in a time-honoured
meaning dating back at the least to Darwin’s Origin
of Species) or because they descend with convergence from separate ancestral genes (i.e., are analogous). It is nevertheless possible that the restrictions
imposed by a functional fitness may cause sufficient
convergence to produce an apparent genetic relatedness. Therefore, the demonstration that two presentday sequences are significantly similar, by either chemical or genetic criteria, still must necessarily leave
undecided the question whether their similarity is
the result of a convergent process or all that remains
from a divergent process. For example, it is at least
philosophically possible to argue that fungal cytochromes c are not truly homologous to the
metazoan cytochromes c, i.e., they just look
homologous.
Colin Patterson made a similar argument [39], explicitly pointing out that statistically significant sequence
similarity does not necessarily force the conclusion of
homology:
… given that homologies are hypothetical, how do
we test them? How do we decide that an observed
similarity is a valid inference of common ancestry? If
similarity must be discriminated from homology, its
assessment (statistically significant or not, for example) is not necessarily synonymous with testing a
hypothesis of homology.
How, then, would we know if highly similar biological
sequences had independent origins or not? In all but the
most trivial cases we do not have direct, independent
evidence for homology — rather, we conventionally
infer the answer based on some qualitative argument,
often involving sequence similarity as a premise. One
purpose of my original analysis [1] was to give this verbal argument a formal basis, using modern evolutionary
models and probability theory. Perhaps the E-values
from Karlin-Altschul statistics have already solved this
problem from a statistical perspective [41-43]? As I
explain in detail below, such is not the case. The most
that a low E-value for sequence similarity (say, from a
BLAST search) can do is show that the observed degree
of sequence similarity is greater than that expected by
random chance — the assessment of homology, on the
other hand, is a distinct question. Furthermore, KarlinAltschul tests for similarity miss a critical aspect of
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evolution that phylogenetic models readily grasp: the
hierarchical structure of nested correlations induced in
genetic sequences by genealogical processes.
Logical problems and misconceptions with BLAST-style
null hypothesis tests
A main motivation for my original analysis [1] was to
escape from the logical quagmire posed by frequentist
null hypothesis tests and bring state-of-the-art probabilistic methods (Bayesian and likelihoodist) to bear on the
question of UCA. My tests of common ancestry are very
pointedly conducted within a Bayesian and model-selection framework, eschewing frequentist null hypothesis
methodology — a point made very prominently in the
original report.
Nevertheless, in their criticism K&W state that they
“interpret these tests [of common ancestry] within the
null hypothesis framework.” The reviewers for K&W’s
criticism similarly expect a null hypothesis in my analysis, ask whether I am using the Fisher or NeymanPearson methodology of null hypothesis testing, and
claim that small P-values directly support a common
ancestry hypothesis [2]. Due to these misconceptions
about both my model selection methodology and the
capabilities of frequentist null hypothesis tests, I find it
necessary to explicitly lay out the advantages of the
former and the logical problems with latter. Those
who are familiar with Bayesian inference and model
selection theory, and with the standard criticisms of
frequentist null hypothesis tests, may wish to skip to
the end of the Introduction where I specifically discuss
K&W’s simulation.
Frequentist hypothesis tests (of both Fisher and Neyman-Pearson flavors) have been highly criticized and
disparaged for many decades by professional statisticians
[44-71]. These criticisms are well-known in statistics —
they in fact currently reflect the consensus view — and
as such I make no claims of originality in the following.
I begin with a representative quote from Jeff Gill, current Director of the Center for Applied Statistics at
WUSTL, writing for social scientists, but the criticism
applies generally:
The null hypothesis significance test (NHST) should
not even exist, much less thrive as the dominant
method for presenting statistical evidence in the
social sciences. It is intellectually bankrupt and deeply flawed on logical and practical grounds. More
than a few authors have convincing demonstrated
this [54].
Gill goes on to list 33 high-profile supporting publications by mainstream statisticians from over the past half
century.
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E-values, P-values, and Karlin-Altschul statistics
A BLAST E-value is a Fisherian null hypothesis significance test [41-43,72]. With BLAST searches, the null
hypothesis holds that the observed level of sequence
similarity is an artefact generated by the optimal alignment of two random sequences [41-43,72].
To conduct a Fisherian null hypothesis significance
test, a P-value is calculated based on a “null” distribution of some relevant statistic of the data. The P-value is
interpreted as the weight of evidence against the null
hypothesis; the smaller the P-value, the greater the evidence against the null. A P-value is defined as the probability of obtaining a value of the test statistic at least as
extreme as the actual observed value, assuming that the
null hypothesis is true. More formally, we say that the
P-value = p(D|N), read as the conditional probability of
D given (or assuming) N, where D is data equal to or
more extreme than the observed value, and N is the
null hypothesis.
In Karlin-Altschul statistics of sequence similarity, two
sequences are optimally aligned by maximizing the similarity between them [41-43]. The similarity between two
sequences is quantified by a similarity statistic, or similarity score, S. Conventionally, the similarity score is
found by a weighted sum of the aligned positions
between two sequences, in which the weights are given
by a log-odds amino acid scoring matrix, such as the
BLOSUM62 matrix [73]. If we take a large number of
random sequences and align them (by maximizing the
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similarity score S), we will obtain a distribution of similarity scores. It has been found empirically that random
similarity scores closely follow an extreme value distribution (EVD). An EVD has a bell-shaped curve, somewhat similar to a Gaussian, but is asymmetric with a
longer right tail (see Figure 1).
For Karlin-Altschul statistics, then, the null distribution is the EVD of random similarity scores, where the
similarity score is the appropriate test statistic. Imagine
that we align two protein sequences and obtain the
observed, optimal similarity score S for the alignment.
The P-value is then the probability of that score or
greater, as given by the EVD of random sequence alignments. This probability is also known as the “tail probability”, as it quantifies the probability in the rightmost
tail of the EVD (shown as the shaded region of the
extreme value distribution in Figure 1).
Note that there is a close relationship between Pvalues and E-values. An E-value is similarly defined as
the average number of times we expect to obtain a
value of the test statistic at least as extreme as the value
actually observed, assuming that the null hypothesis is
true. For mostly historical reasons, the E-value is conventionally used more often in sequence similarity tests,
like BLAST searches, and it can be directly calculated
from the P-value:
E = - ln(1 - P)
(1)
Figure 1 Extreme value probability distribution for similarity scores. A standard extreme value distribution (EVD) is shown. In Karlin-Altschul
statistics, similarity scores (S) for alignments of random sequences are assumed to follow an EVD. P-values are based on the tail probability,
shown as the shaded blue area, corresponding to the probability of observing a similarity score greater than or equal to the observed similarity
score (So) for a given alignment of interest.
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For small values of the P-value (< 0.05), both measures are approximately equivalent. The important point
here is that for our purposes E- and P-values are interchangeable, and all the arguments made below apply
equally to both.
As mentioned above, a low P-value (or E-value) is
conventionally considered to be a measure of evidence
against the null hypothesis; the smaller the P-value, the
more reason we have to believe that the null is false.
The logic behind this interpretation of the P-value is
neatly summarized by Ronald Fisher’s famous disjunction: Upon obtaining a small P-value, “Either an exceptionally rare chance has occurred, or the theory of
random distribution is not true” (italics in original) [74].
For the moment, let us assume that this reasoning is
valid — that a small P-value is indeed evidence against
the null. We will revisit this assumption later.
Although the logical problems with null hypothesis
statistical tests are many and profound, here I recount
only three faults that are most pertinent to homology
inference using a BLAST-style null hypothesis test for
sequence similarity based on Karlin-Altschul statistics.
The False Dichotomy: Rejecting the null does not imply
acceptance of a favoured alternative hypothesis
According to the logic of null hypothesis testing, a small
P-value allows us to reject the null hypothesis at some
specified “level of significance” [47,57,64,65,74-76]. By
convention, a meaningful level of significance is often
chosen as 0.05 or 0.01, though other values are frequently used depending on the application (e.g, PSIBLAST by default uses a 0.005 cut-off [77]). P-values
smaller than the chosen significance level allow us to
“reject the null hypothesis” as false. Nevertheless, rejecting the null hypothesis of an alignment of random
sequences is not logically equivalent to accepting common ancestry. This reasoning could be valid only if ‘randomness’ and ‘common ancestry’ were mutually
exclusive hypotheses, but the logical complement of ‘a
random alignment’ is ‘not a random alignment’, rather
than ‘common ancestry’. Non-random, significant
sequence similarity can be due to many factors besides
common ancestry.
The common belief that a small E-value indicates
sequence homology (i.e., that the two sequences share a
common ancestor) is based on a false dichotomy. During the 1981 creationist trial in Little Rock, Arkansas,
the attorney for the State, David Williams, committed
the same logical fallacy by arguing that criticisms of evolutionary theory were evidence for creationism. Geneticist Francisco J. Ayala, a witness for the plaintiffs,
corrected him:
… negative criticisms of evolutionary theory, even if
they carried some weight, are utterly irrelevant to
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the question of validity or legitimacy of creation
science. Surely you realize that not being Mr Williams in no way entails being Mr Ayala! [78]
Clearly, I am not attorney Williams (with high statistical significance, P < 0.01), and just as clearly, the fact
that we have established that I am not Williams does
not imply that I am Dr Ayala. Likewise, not being an
alignment of random sequences in no way entails being
homologous.
If our aim is to establish my true identity, we could,
one-by-one, rule out the possibilities that I am William
Martin, or Eugene Koonin, or Yuri Wolf, or one of the
other ~ 7 billion people on the planet. But wouldn’t it
be useful if we had a method that instead could directly
provide positive evidence that I am Douglas Theobald?
Unfortunately, null hypothesis significance tests are
incapable by design of providing evidence for any
hypothesis — null hypothesis tests are intended to only
provide evidence against the null, no more nor less [75].
Hence null hypothesis tests, by their own frequentist
logic, cannot provide evidence for common ancestry.
P-values cannot provide evidence for the null hypothesis
Furthermore, failing to reject the null, by obtaining a
large P-value (e.g., P ≫ 0.05), does not imply that the
null is true [75]. As Sir Ronald Fisher, inventor of the Pvalue and null hypothesis significance test, wrote: “It is a
fallacy so well known as to be a standard example, to
conclude from a test of significance that the null
hypothesis is thereby established;… “ (emphasis in original) [74]. Similarly, Fisher wrote that “it should be noted
that the null hypothesis is never proved or established,
but is possibly disproved, in the course of experimentation” so that “experimenters … are prepared to ignore
all [insignificant] results” [79,80]. This is often stated as
the maxim: “failing to reject the null does not mean
accepting the null”, or, more prosaically, “Thou shalt
not draw inferences from a nonsignficant result!” [81].
For example, according to the logic of null hypothesis
significance testing, an E-value of 10 does not mean that
the sequence alignment is likely to be random — it simply means that a random alignment could easily have
resulted in the observed level of sequence similarity.
Clearly it would be beneficial to have a statistical
method that could provide evidence for the null and not
just evidence against it.
The “Prosecutor’s Fallacy” and pregnant women:
Improbable data does not imply an improbable hypothesis
Up till now, we have assumed that the frequentist position is correct, namely that Fisher’s disjunction has logical force and a small P-value is evidence against the null
hypothesis. But even this key premise is fallacious, as it
relies on a notorious error of probabilistic reasoning
known in law as the “Prosecutor’s Fallacy” [82,83]. A
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small P-value, which measures the improbability of the
data under the null, in fact does not imply that the null
is improbable.
The Prosecutor’s Fallacy arises from incorrectly inferring that a cause is unlikely because the effect is unlikely. A simple example may suffice to illuminate the
problem. A quick glance around should establish that, at
any given time, most women are not pregnant. In my
state of Massachusetts, for example, the frequency of
women that are pregnant is approximately 2% [84]. We
can quantify this observation with a conditional probability statement: the probability that a particular person
is pregnant, given that the person is a woman, is 0.02.
Symbolically, we write p(P|W) = 0.02, where P is the
proposition that “this person is pregnant” and W is the
proposition that “this person is a woman”. Note that p
(P|W) is small — in fact small enough to be “statistically
significant” by convention. Nevertheless, the small value
for p(P|W) does not imply that the inverse probability,
p(W|P), is also small. The probability that ‘this person is
a woman given that this person is pregnant’ is obviously
much greater than 0.02!
The same rules of probability necessarily apply to p(D|
N) (the P-value) and the inverse probability p(N|D) (the
probability of the null hypothesis given the observed
data). Thus, a small P-value does not imply that the null
hypothesis is unlikely. In fact, by itself, the P-value tells
us nothing at all regarding the probability of the null
hypothesis. The only way to calculate the probability of
the null hypothesis, p(N|D), is by using Bayes theorem,
but frequentist methodology does not allow us to do
that.
The reason why the Prosecutor’s Fallacy is false is
simply because true hypotheses routinely predict lowprobability data. Observing a piece of data that is unlikely could be nothing more than that — unlikely things
happen all the time (like pregnant women or a winning
lottery ticket). The null hypothesis may predict the
observed data with a small probability, resulting in a
small P-value, but if competing models are even worse
— that is, competing models predict the same data with
even lower probability — then why should we reject the
null? For these reasons, there is no logical reason to
think that the null hypothesis is likely to be false based
solely on a small P-value; additional information is
required.
A way out: Bayes, likelihood, and model selection
Model selection methods, such as log likelihood ratios
(LLR), the Akaike Information Criterion (AIC), and
Bayes factors [47], are now used routinely in modern
biological research, especially in phylogenetics, genetics,
and bioinformatics [69,85-95]. Model selection theory
has largely been developed as an alternative to null
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hypothesis significance tests, such as Fisherian P-values,
which were developed within the frequentist statistics
paradigm. The advantages of model selection methods
include a firm logical and theoretical basis and elegant
handling of model complexity, both of which make
them attractive for analyzing complex evolutionary models for biological sequence data.
The core idea is elegantly simple: Quantitatively calculate how well different models explain the data (judged
either by the likelihood of the data or by the posterior
probability of a model), and compare the models to
each other. Alternative models compete against each
other head-to-head, and the observed data is the judge.
From a likelihoodist point of view, such as when using
the AIC, the preferred model is just the model that
explains the data best (by assigning it the highest probability). From a Bayesian point of view, the preferred
model is the model that has the highest probability
given the data, within the set of models being evaluated.
The critical part is in having explicit stochastic models
(likelihood functions) for each of the hypotheses under
comparison.
One great advantage of model selection methodology
is how the complexity of competing hypotheses is
handled. When judging the explanatory power of competing hypotheses, two opposing factors must be
accounted for: parsimony and the fit to the observed
data. By increasing the number of parameters in a
model — i.e., by making the hypothesis more complex
— one can always improve the “goodness of fit” to the
data. For instance, when fitting a polynomial curve to a
set of points, the discrepancy between the curve and the
data points can be minimized arbitrarily by increasing
the order of the polynomial until it equals the number
of data points. However, simpler models are preferred,
since increasing the complexity of the model increases
the uncertainty in the estimates of the parameters. The
fewer ad hoc parameters, the better — a principle informally known as Occam’s Razor. P-values unfortunately
have no way to account for model complexity. Model
selection methods, in contrast, weigh these two opposing factors (goodness-of-fit and complexity) to find the
hypothesis that is jointly the most accurate and the
most precise.
Model selection methodology solves all the problems
with null hypothesis significance test P-values enumerated above. First, in model selection methodology, there
is no null hypothesis. All hypotheses are treated equally,
none is given special favoured status, and they compete
head-to-head. There is no need to rely on a false dichotomy, since multiple models are compared directly to
each other. A hypothesis is “rejected” only if there is a
better alternative. Second, model selection scores provide the evidence for each hypothesis, not just against
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the “null”. The complexity and ability of a model to
explain the data is the evidence for and against it, when
compared to other competing hypotheses. Third, model
selection methodology does not fall prey to the Prosecutor’s fallacy. A particular model A may predict the data
with a small probability, but if no other hypothesis does
any better (after accounting for model complexity), then
model A is the preferred hypothesis. Fortunately, in
model selection theory pregnant women are not
rejected.
In my formulation of the tests for UCA, independent
ancestry models are represented by multiple phylogenetic trees, one tree for each group of taxa that is
assumed to be genealogically related under this particular model [1]. Unrelated taxa are found in different
trees. Because each tree is assumed to be independent
(by definition of independent ancestry), the complete
probability of the data assuming an independent ancestry model is simply the product of the probabilities of
the several trees that compose it. For instance, consider
two independent, unrelated trees of taxa A and B, and
the sequence evidence X. The total probability of the
sequence data X for the independent ancestry hypothesis
IA is given by the joint probability of the data from tree
A and tree B:
p(X | IA) = p(X | A& B) = p(X | A)p(X | B)
(2)
Common ancestry models are represented by including all taxa in unified trees. Once ‘common ancestry’
and ‘independent ancestry’ are thus defined for a set of
taxa, it is straightforward to apply the model selection
tests to determine which hypothesis is best.
Koonin and Wolf’s rebuttal: Common ancestry models
win in a simulation of similar sequences lacking
phylogenetic structure
In a recent criticism of my model selection tests of
UCA, Koonin and Wolf argue that the test results do
not support the conclusion of universal common ancestry [1,2]. K&W support this claim by a simulation study
in which similar sequences were randomly generated
without any phylogenetic structure. In K&W’s simulation, each column of a sequence alignment has a different, independent amino acid distribution (the amino
acids are distributed according to a discrete distribution,
also called a categorical distribution [96,97]). They then
generated artificial sequences by randomly selecting
amino acids from each column’s distribution. The stochastic model corresponding to this simulation I will
call the “profile” model, due to its similarity to common
sequence profiles [98-100]. The profile model can be
considered a star-tree in which each site has its own
amino acid substitution matrix, and hence it cannot
model phylogenetic structure or different levels of
sequence similarity. K&W’s simulated data has no phylogenetic signal in the sense that the sequences lack
nested patterns of similarities. For this artificial data set
generated by the profile model, the model selection tests
choose common ancestry over independent ancestry.
K&W make three distinct claims based on their simulated data:
(1) the model selection tests prefer UCA solely due to
the high similarity of the protein sequences, regardless
of genealogical history,
(2) their simulation corresponds to a convergent, independent ancestry model, and therefore the model selection tests err in choosing common ancestry for the
simulated sequences,
(3) the demonstration of UCA is dependent on the
assumption that proteins with highly similar sequences
share common ancestry.
All of these claims are incorrect, and I consider each
of them in turn below.
Results and Discussion
Claim 1: The conclusion of common ancestry is primarily
due to genealogical structure in the protein sequences,
not mere similarity
In their Abstract, K&W make their main claim:
…the purported demonstration of the universal common ancestry is a trivial consequence of significant
sequence similarity between the analyzed proteins.
The nature and origin of this similarity are irrelevant
for the prediction of “common ancestry” of by the
model comparison approach.
Later they further explain that the model selection
results in favour of UCA are “simply a restatement of
the fact that these proteins display a highly statistically
significant sequence similarity”. Reviewer William Martin agrees: “They are absolutely right on this”.
I present four different evidences demonstrating that
K&W’s primary claim — that my results are independent of phylogenetic history and are simply due to
sequence similarity — is incorrect. The first piece of evidence is based on mathematical considerations of the
theory behind the phylogenetic models used in the tests,
while the final three are empirical.
I. Phylogenetic models involve more than mere sequence
similarity
Based on the theory underlying modern phylogenetic
models, we know that sequence similarity is only one
component that indirectly affects the model selection
tests [31,101,102]. Each of the models, whether common
ancestry or independent ancestry, involve phylogenetic
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trees. Trees are mathematical structures that can
account for both gross similarity (largely in the branch
lengths) and subtle patterns of similarities (in the particular topology of the tree) [31,101,102]. It is this latter
component — the complex hierarchical patterns of similarities induced by a genealogical branching process —
that phylogenetic trees can account for but methods like
BLAST, which consider only overall sequence similarity,
cannot.
Consider the phylogenetic tree of six protein
sequences shown in Figure 2. In standard Markovian
phylogenetic models, such as the ones used in the
model selection tests, the probability of the six
sequences depends on the topology of the tree and its
branch lengths [31,101]. The sum of the branch lengths
between two sequences is proportional to the number of
evolutionary substitutions separating those two
sequences. In this sense, the total distance along the
tree between two sequences is a measure of their similarity. Importantly, if you change the topology, while
maintaining the same distance between two sequences,
or even maintaining the same total tree length, you generally change the likelihood of the model (i.e., you
change the probability of the sequences).
Now imagine that you replace these six sequences
with a different set that nevertheless has identical percent identity and similarity as the original set (perhaps
as measured by an alignment score using a substitution
matrix). In general this replacement will also change the
likelihood, even if the topology and branch lengths are
held constant. This means that the likelihood of a tree is
not simply a function of the similarities of the sequences
[31,101,102]. Rather, the likelihood of a phylogenetic
tree is also a function of the nested pattern of similarities in the data. Therefore, the model selection tests,
which are explicitly based on likelihoods of trees, consider information in the sequences that cannot be
reduced to simple sequence similarity.
Hence it is possible for highly similar sequences to
nevertheless have conflicting hierarchical structure that
does not fit well to a single, global tree. Common ancestry implies phylogenetic structure; Markovian character
evolution along a bifurcating tree results in hierarchical
patterns of correlated character changes. If the phylogenetic structure in a set of highly similar sequences is
conflicting, then this is evidence against common ancestry, and it could be evidence for independent ancestry
models that do not force the proteins into a global phylogeny. This is one key advantage of my model-based
tests over simple BLAST-type analyses that only look at
gross sequence similarity.
K&W quote what they call a “key sentence” from my
Nature letter where I explain the significance of the
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large test scores favouring UCA:
… when comparing a common-ancestry model to a
multiple-ancestry model, the large test scores are a
direct measure of the increase in our ability to accurately predict the sequence of a genealogically
related protein relative to an unrelated protein.
Later they claim that this sentence is “simply a restatement of the fact that these proteins display a highly statistically significant sequence similarity”. However, from
the considerations given above, we know that a phylogenetic model’s ability to predict a given sequence (e.g.,
sequence D in Figure 2) from other sequences (e.g.
sequences A, B, C, E, F in Figure 2) is a function of the
tree topology and the patterns in the sequences, not
simply of the gross similarities among the sequences.
II. High sequence similarity is insufficient to force the
conclusion of common ancestry
If K&W’s hypothesis is correct — that the model selection tests choose common ancestry simply due to
sequence similarity — then the tests should choose
common ancestry over independent ancestry for any set
of sequences with highly statistically significant
sequence similarity. K&W make this very claim in their
Discussion: “The likelihood tests of the kind described
by Theobald … yield results ‘in support of common
ancestry’ for any sufficiently similar sequences.” However, this prediction is directly contradicted by the
example given in the Supplementary material of my original Nature letter (section 4.3, pages 16-20 [1]). There
I present a simple case in which the model selection
tests choose independent ancestry for sequences with
highly significant similarity. Here I present another
similar example, in which four sequences have highly
significant similarity to each other (in all possible pairwise comparisons, Table 1), and yet the model selection
tests prefer independent ancestry models over common
ancestry (Table 2). Therefore, the model selection tests
necessarily consider factors other than mere sequence
similarity, and highly significant sequence similarity is
not sufficient for the model selection tests to choose
common ancestry.
Why do the model selection tests favour independent
origins for these sets of sequences, in spite of significant
similarity? The answer is that these similar sequences
have conflicting phylogenetic structure, and conflicting
phylogenetic correlations are unlikely to have been generated by a common ancestry process. The known presence of conflicting phylogenetic structure in the
universal protein data set I used [103] (as indicated by
suspected horizontal gene transfer events) was in fact a
major motivation for my model selection tests of UCA
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Figure 2 Example phylogeny. A toy phylogeny of six sequences, represented by the letters A-F.
— it is possible that a high enough degree of conflicting
phylogenetic structure could indicate that a particular
independent ancestry hypothesis is a superior model for
the universal protein data.
III. Star tree models account for similarity, but not for
genealogical structure in the real protein data
K&W suggest that the universal proteins in my dataset
could have been generated by a process completely
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Table 1 Significant similarity among four artificially
constructed sequences.
Table 3 Model selection scores for Koonin and Wolf’s
artificial data.
Sequence
E
M
P
Model
ln marginal lik (+/- SEM)
B
4e-50
1e-17
1e-27
profile
-7521 (21)
0
4e-31
1e-17
CA
-7646 (20)
125
2e-36
Star
-7813 (20)
292
IA
-8164 (14)
643
E
M
E-values from pairwise BLAST comparisons between four protein sequences
(called B, E, M, and P), as reported by the NCBI bl2seq utility (see Appendix 2,
Additional File 1 for the sequences).
lacking all phylogenetic structure, namely their profile
model. However, there are very compelling a priori reasons to suspect that K&W’s hypothesis should be false.
The strong phylogenetic structure in the universal protein data set I used (and in similar data sets in the literature) is well established, and trees based on this
dataset have local regions of high topological support
[103,104]. Nevertheless, it would be useful to quantify
the amount and influence of phylogenetic structure, as
opposed to mere sequence similarity, in the universal
protein data.
One way to formally test for phylogenetic structure is
to see how well the data is explained by a star tree. Star
trees model varying degrees of similarity among a set of
proteins, as each branch in the star tree can be a different length, but star trees cannot account for hierarchical
genealogical patterns. In fact, according to the model
selection criteria, star trees explain K&W’s simulated
data much better than independent ancestry models (by
several hundred log likelihood units, see Table 3). In
contrast, star-tree models are extremely poor models for
the universal protein data — they are actually worse
than independent ancestry models (differences in loglikelihood greater than 20,000, see Table 4). Thus, the
Table 2 Model selection scores for four artificially
constructed, significantly similar sequences.
Model
ln Lik
LLR
K
∆AIC
CA (BEMP)
-5411
0
25
0
IA (BE+MP)
-5092
-319
44
-300
IA (BM+EP)
-5009
-402
44
-383
IA (BP+EM)
-5038
-373
44
-354
IA (E+BMP)
-5115
-296
42
-279
IA (M+BEP)
-5128
-283
42
-266
IA (P+BEM)
-5060
-351
42
-334
IA (B+EMP)
-5022
-389
42
-372
Common ancestry is compared with various independent ancestry models for
four sequences with highly significant similarity to each other (see Appendix
2, Additional File 1 for the sequences). CA, common ancestry; IA, independent
ancestry; LLR, log-likelihood ratio; K, number of parameters in model; AIC,
Akaike information criterion. Model selection scores are relative to the
common ancestry model; negative scores (LLR and ∆AIC) indicate better
models. Independent ancestry model “BE+MP” indicates that B and E are
homologous to each other, and that M and P are homologous to each other,
yet B and E have an independent ancestry from M and P.
ln BF
Log marginal likelihoods and Bayes factors for Koonin and Wolf’s artificial
data. Values reported are averages and standard error of the mean (SEM) for
the 100 simulated alignments. CA, common ancestry; IA, independent
ancestry; BF, Bayes factor
universal proteins display significant genealogical structure that is even more important than sequence
similarity.
IV. Koonin and Wolf’s “sequence similarity only” profile
model does not explain the universal protein data
Most importantly, we can directly test K&W’s profile
model against both common ancestry and independent
ancestry models and see if the profile model can adequately explain the sequence data. The profile model
can account for neither phylogenetic structure nor differing degrees of sequence similarity, as it is essentially a
symmetrical star tree where each site has a different
substitution matrix of amino acid exchangeabilities. The
profile model is something of a pathological case, since
for these datasets there are roughly as many parameters
as data points (19 parameters per column, giving a datato-parameter ratio of 1.05 for K&W’s artificial dataset,
0.63 for the universal protein dataset). The low data-toparameter ratio invalidates the AIC and non-nested LLR
tests, as it strongly violates the approximations needed
to justify the tests (the AIC and LLR are strictly only
valid in the asymptotic limit of infinite data) [94,105].
Bayes factors, however, do not suffer from this limitation [106], and there is a conveniently simple analytic
expression for the marginal likelihood of the profile
model (see the Appendix, Additional File 1).
Table 4 Model selection scores for the universal protein
data.
Model
ln marginal lik
ln BF
CA (ABE)
-126,713
0
IA (AE+B)
-133,602
6,889
IA (AB+E)
-134,744
8,031
IA (BE+A)
-135,201
8,488
IA (ABE_M +M)
-138,899
12,186
IA (A+B+E)
-140,578
13,865
IA (ABE_H +H)
-140,713
14,001
star
-148,883
22,170
profile
-151,145
24,432
Log marginal likelihoods and Bayes factors for the real, universal protein data
set.
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According to the Bayes factors, K&W’s artificial data
is best explained by the profile models, which are preferred over the common ancestry models (see Table 3).
This is expected, as K&W’s artificial data was simulated
under the profile model. However, for the universal protein data set used in my paper, the profile models are
extremely poor compared to common ancestry (log-likelihood differences 30,000, Table 4) — much worse even
than independent ancestry models. Therefore, contrary
to K&W’s hypothesis, similarity alone cannot explain
the complex sequence correlations observed in the universal protein data set.
artifactually choose common ancestry for convergent
proteins. Reviewer Ivan Iossifov (of the K&W comment)
agrees and claims that K&W “perform a simulation
experiment which clearly demonstrates… Theobald’s
method chooses UCA hypothesis with virtual certainty
over data generated by a convergent evolution model.”
However, K&W never state the assumptions of their
proposed convergent hypothesis, nor do they derive a
stochastic model from those assumptions. We therefore
have no reason to believe that the simulation generates
artificial convergent proteins. Rather, as detailed below,
the simulated sequences mimic homologous proteins.
For the real data, hypotheses that model phylogenetic
structure are best, those that model sequence similarity
alone are worst
Homologous sequences may be statistically independent
For the real, universal data set, the models are ordered
as follows, best to worst: common ancestry > independent ancestry > star tree > profile model. This ordering
indicates that phylogenetic structure is an extremely
important factor for the real data set, actually more
important than gross sequence similarity (unlike K&W’s
artificial data set). The common ancestry models can
adequately account for phylogenetic structure and
sequence similarity, so they are best. The independent
ancestry models also can account for the phylogenetic
structure within each independent group of related
sequences cannot account for similarity between the
groups. Nevertheless, independent ancestry models are
better than the star tree and profile models, which can
account for sequence similarity but lack all phylogenetic
structure.
For K&W’s artificial data, in contrast, the profile
model is best and the independent ancestry model is
worst. K&W’s simulated data has no phylogenetic, hierarchical structure. The profile model is the true generating model for the simulated data, and it accounts for
the different evolutionary processes at each site in a way
the other models cannot, so clearly it should be preferred. Since sequence similarity is the only factor in
their artificial data set, the independent ancestry models
will be the worst, as they cannot adequately account for
sequence similarity between two or more groups. The
fact that common ancestry models are preferred over
independent ancestry is also unsurprising. As discussed
below, K&W’s profile model is a common ancestry
model, and therefore produces artificial sequences that
mimic homologous sequences.
Claim 2: Koonin and Wolf’s simulation corresponds to a
common ancestry model
K&W assert, without proof, that the profile model used
in their simulation produces “phylogenetically unrelated
sequences”. Hence they believe they have presented a
counterexample where my model selection tests
First, consider the justification K&W provide for why
they their simulation produces convergent sequences:
… these [simulated] alignments contain no signal of
common ancestry (in more general terms, no evolutionary signal) whatsoever because each position in
each sequence is generated independently from
other positions.
If this claim were true, it would invalidate nearly all of
modern phylogenetics, since the standard evolutionary
models assume site independence, i.e., that the evolutionary change at each position is independent of other
positions [31,101]. The “independent sites” assumption
is admittedly a convenient approximation, a simplification that is likely valid for a large majority of potential
site interactions but invalid for a small fraction of interacting sites. However, there is no reason that different
sites in homologous proteins cannot evolve independently (many do), and therefore the fact that each position in K&W’s simulated alignments is independent in
no way implies non-homology.
K&W’s profile was constructed from likely homologs
To produce their simulated sequences, K&W constructed a frequency profile from a large set of universally conserved proteins that most biologists believe to
be homologous (including Koonin, Wolf, and their
reviewers [2]). At the very least, the fact that their simulation method is based on real universally conserved
proteins suggests that sequences generated by their
simulation will reflect, to some extent, whatever real
process actually produced those conserved proteins. If,
to take an obvious example, the proteins they based the
simulation on are indeed homologous, then sequences
produced by K&W’s simulation method will be strongly
biased to look like bona fide homologous sequences.
The simulated alignments were produced by a well-known
common ancestry model
In fact, the K&W profile model is a special case of a
common ancestry model that has been described previously in the phylogenetic literature. K&W’s profile
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model is a phylogenetic, common ancestry model, where
each site has its own reversible amino acid substitution
process and independent set of equilibrium frequencies,
in which the proteins have evolved according to a star
tree with equal branch lengths. This model was first
considered by Bruno in 1996 [98,107]. Lartillot and Philippe 2004 refer to it as the MAX-Poisson model with
uniform site rates (it is a special case of their CAT models), and they implement it in the phylogenetic software
PhyloBayes [100] and PhyML-CAT [108]. Hence, the
K&W simulation is invalid as a counter-example, since
my model selection tests correctly choose common
ancestry over independent ancestry for the simulated
homologs.
A common ancestry model based on homologous
sequences should not simulate convergent proteins
With these points in mind, let me restate exactly what
K&W did in their simulation. They constructed a frequency profile from a large set of universally conserved
proteins that most biologists believe to be homologous.
Then they used this profile to generate sequences with
the MAX-Poisson common ancestry model. Finally, they
performed my model selection tests on this artificial
sequence data set, finding that the tests favour common
ancestry. It is difficult to understand how one could
possibly conclude from this simulation that the model
selection tests are behaving improperly.
K&W’s simulated sequences lack phylogenetic signal
in the sense that the sequences lack correlated hierarchical structure. But lacking hierarchical structure does
not necessarily imply that the sequences are independent evolutionary inventions (though a lack of phylogenetic structure may decrease the probability of common
ancestry relative to competing hypotheses that predict a
lack of structure). As mentioned earlier, star trees are
bona fide common ancestry models that lack hierarchical structure. A star tree is a phylogeny, after all.
Claim 3: The conclusion of homology does not involve
circular logic
Several critics, including K&W and their reviewer
Arcady Mushegian [2], have suggested that the model
selection tests for common ancestry implicitly involve
“hidden” circular logic of some sort. Here I consider
several of the potential sources of circularity, including
issues involving sequence similarity, models of sequence
evolution, and sequence alignment.
Model selection tests do not assume that sequence
similarity implies homology
K&W claim that the conclusion of UCA, based on my
model selection tests, requires “the assumption that universally conserved orthologous proteins with highly similar
sequences actually originate from common ancestral
forms”. However, this contradicts the logic of model
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selection tests. Common ancestry models of course
assume that the sequences they model are homologous.
On the other hand, independent ancestry models assume
that only certain subsets of sequences are homologous.
The only other assumptions made by these models are the
standard phylogenetic assumptions: that the evolution of
homologous proteins proceeds by a standard Markovian
model of sequence evolution (that is time-stationary,
reversible, and site-homogeneous), that each site in the
proteins is independent, and that new homologous proteins are generated by gene duplication events (lineage
splitting) represented by bifurcating trees. Importantly,
however, there is no assumption about which of these
models is correct, and there is no assumption that “highly
similar sequences are homologous”. The winning model is
dictated, objectively, by how well it explains the data relative to the other models. In other words, the model selection tests tell us which model, and hence which set of
corresponding assumptions underlying that model, is best.
The results could have pointed to independent ancestry,
but that’s not the answer this real data set gave.
Using amino acid substitution matrices does not imply an
assumption of homology
One of the main assumptions underlying the phylogenetic models is that homologous sequences have evolved
by a Markovian process of amino acid residue substitution, described by a 20 × 20 matrix of substitution rates.
The popular rate matrices, such as WAG [109] and LG
[110], were originally constructed from large alignments
of ostensibly homologous protein sequences. However,
for the formal purposes of the model selection tests, we
do not actually know that the rate matrices were based
on homologous sequences. We do know that similar
sequences were used in constructing the rate matrices,
but recall that similarity is not necessarily homology.
From a model-selection perspective, the origin of the
substitution matrices is irrelevant — the likelihood function does not know where the matrices came from, and
the likelihood is the final judge. All that matters is that
some substitution matrices result in higher model selection scores than others. The origin of a hypothesis is of
no relevance to how it fairs when tested in a model
selection method (arguing otherwise would be committing a type of “genetic fallacy”). Furthermore, the majority of the variance in rates in a substitution matrix can
be captured by a single chemical property, namely
hydrophobicity [111]. This strongly suggests that the differing rates in a substitution matrix are due to biophysical factors, rather than common ancestry (as first
discussed by Zuckerkandl and Pauling [14]).
A sequence alignment does not necessarily represent
homologous sites
Sequence alignments are often interpreted as representing a homology hypothesis, since each column in an
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alignment can show which residues in a sequence are
related by common ancestry. Under this interpretation,
using a fixed alignment in the model selection tests for
common ancestry may seem to assume common ancestry from the outset. But this is only one possible interpretation of a sequence alignment. The similarities
shown in an alignment between specific residues may be
due to homology or analogy. Sequence alignment is
nothing more than a procedure for maximizing similarity, and it is unnecessary to assume common ancestry to
maximize similarity.
As a concrete example, it is common practice in
SELEX experiments to align RNA aptamer sequences
(with themselves and with natural sequences) in order
to find common motifs, in spite of the fact that the
aptamer RNAs may be known to each have independent
origins from a random sequence library [112]. In this
case aligned positions do not represent homologous
residues, but rather functionally analogous residues.
Similarly, one can align promoter sequences to find
common motifs, without assuming that the promoters
actually originated by descent from a common ancestral
sequence [113]. An alignment can also be generated
from pure three-dimensional structural data, even for
proteins known to be unrelated [114,115]. The resulting
structure-based alignment depicts structurally analogous
residues, not homology. Therefore, an alignment is not
necessarily a proposal of homology, because similar
aligned sequences may be merely structurally or functionally analogous.
Alignment algorithms can bias the tests towards common
ancestry with weakly similar sequences
It is possible that the process of sequence alignment can
bias the results of the tests towards common ancestry
[116]. By maximizing residue matches, sequence alignment algorithms can artifactually induce similarities
between unrelated sequences. In certain extreme cases
these artifactual similarities can prejudice the model
selection tests towards common ancestry if the alignment bias is large and unaccounted for.
The effect of alignment bias is maximal for random
sequences where it results in a highly uncertain alignment with spurious similarities; it is minimal for
sequences of high similarity where the alignment is relatively certain; and the bias vanishes in the limiting case
of long identical sequences where no alignment uncertainty exists. Accounting for alignment bias and uncertainty would be an important consideration for testing
homology hypotheses in cases of very little sequence
similarity. However, it has a negligible effect on the tests
of common ancestry reported in my original Nature letter [1], which were based on universally conserved proteins with relatively high sequence similarity.
Furthermore, the Brown dataset used in my original
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report had ambiguously aligned regions removed [103],
including all indels, essentially eliminating any potential
alignment bias and resulting in a very high confidence
alignment.
If alignment bias is suspected to be a significant factor
for a set of dissimilar sequences, then there are several
ways to account for it using the model selection tests
for common ancestry.
First, in a Bayesian framework, one can simply substitute BAli-Phy [117] for MrBayes [118] in the model
selection tests. BAli-Phy elegantly handles alignment
bias and uncertainty by treating the alignment as a parameter and integrating over it. BAli-Phy is unfortunately
much more computationally intensive than using
MrBayes, and thus should be used only when absolutely
necessary. Nevertheless, I have repeated the Class II
Bayes factor model selection tests of UCA with BAliPhy, and the results closely recapitulate those using
MrBayes, as fully expected when using similar
sequences.
Second, one can rather easily estimate an upper bound
for the effect of alignment bias by randomly permuting
the sequences, realigning them, and performing the
model selection tests with PhyML [119] or MrBayes.
The permuted and realigned sequences have no phylogenetic structure, and all similarities in the realignment
are solely due to the alignment procedure. The preference for UCA with the randomly permuted sequences,
as measured by the model selection scores, is then an
estimate of the maximum amount that the alignment
procedure artifactually biases the results towards homology. This control was performed for the universal protein data, and the bias was found to be negligible
compared to the true (unpermuted) model selection
scores (hundreds of log-likelihood units versus thousands, respectively, indicating a maximum ~10% error in
the reported model selection scores).
Finally, if high-resolution structures are available, one
can use structure-based alignments, which do not optimize sequence similarity and hence avoid sequence
alignment bias altogether.
Conclusions
The various results reported here provide a direct refutation of the claim that model selection preference for
UCA is merely a consequence of high sequence similarity [2]. Unlike star trees and K&W’s profile model,
which can only explain sequence similarity, the common
ancestry models can also explain nested hierarchical
sequence correlations. Hierarchical structure in a set of
sequences is a direct prediction of genealogical models,
in which branching of lineages occurs. For the real, universal protein data set, this hierarchical structure is the
overriding factor for the superiority of the UCA
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hypothesis over competing hypotheses, including various
independent ancestry models.
Moreover, the models used in the tests do not assume
a priori that significant sequence similarity implies
homology. Rather, sequence similarity is a consequence
of the common ancestry models, and the common
ancestry models simply explain the data best. Hence, the
strong results from the model selection tests provide a
firm logical basis for relying on the inference from
sequence similarity to homology as a general principle,
as long as there is no strongly conflicting phylogenetic
structure.
As in all of science, our best theories may be incorrect. It is always possible that a biological model may be
proposed in the future that explains the data better than
the UCA models. Clearly I have not tested all possible
models, especially those yet to be developed. I emphasize again here, as I have elsewhere [120], that I have
not provided absolute “proof” of UCA. Proof is for
mathematics and whiskey; it is not found in science.
Nevertheless, these results provide strong evidence for
UCA, given the hypotheses and sequence data currently
available. As it stands, UCA explains the data best by
far. With the model selection framework it is easy to
test a novel, properly specified hypothesis against the
common ancestry models. The profile model proposed
by Koonin and Wolf, however, fails the test.
Methods
Model selection tests were performed as described [1,2].
Star tree models were analyzed using a modified
MrBayes [121], in which a star tree was given to
MrBayes as an initial tree and topology rearrangements
were prohibited. Terminal branch lengths were sampled.
Similar log-likelihoods were found, independently, by
PROML from the PHYLIP phylogenetics package [122],
which allows a star tree as a constrained topology in a
maximum likelihood analysis (this method also found
AIC scores similar to the Bayes factors reported in
Tables 3 and 4). For the Koonin and Wolf profile
model, marginal likelihoods were calculated using Equation 12 in Appendix 1 (see Additional File 1). Koonin
and Wolf’s simulated alignments [2] were generously
provided by Eugene Koonin.
Reviewers’ comments
Reviewer 1: Rob Knight
In this manuscript, the author responds to criticisms of
his prior work that provides a Bayesian framework for
formally testing the hypothesis that all life descends
from a single common ancestor. Specifically, Koonin
and Wolf provided a set of simulations that demonstrate
that the same test will incorrectly identify sequences
with similar composition that are independently
Page 15 of 25
generated as being related. In this paper, several additional tests are provided, including the demonstration
that star phylogenies (in which all sequences stem from
a single common ancestor with no branching structure)
explain the simulated data but not real sequence data,
as does a profile model in which sequences are independently generated from a profile with no phylogenetic
structure. The key conceptual advance is to perform
model selection, rather than to test deviations from a
null hypothesis that may be inappropriate.
Overall, the calculations are convincing, although the
article could benefit from being rewritten in a less combative tone and as a less narrow response to a single
article. I am also somewhat unconvinced by the relevance of the material on the genetic code to the problem of convergent versus divergent protein evolution: a
better example might be the repeated evolution of the
same Trp or Ile active site, each of which has been
demonstrated many times in different selections, which
could provide the basis for truly independent evolutionary origins and which might therefore be interesting to
analyze in the context of the present framework. The
so-called “Welch-mer” also provides a fascinating example of the same site apparently evolving in nature and in
SELEX. I would recommend omitting the section on the
genetic code and replacing it with a discussion on
reproducibility of SELEX, in which area several authors
have done interesting work.
Response: I agree that the issues with the genetic code
are not so relevant to the particular problem of convergent versus divergent protein evolution. That section was
included largely as a response to William Martin,
reviewer of Koonin & Wolf’s comment, where he stated
that my original analysis was guilty of “ignoring the
strength of the universality of the genetic code and the
commonality of central intermediary metabolism among
cells as evidence”. The only point I wished to make was
that, while the near-universality of the genetic code is
strong evidence for UCA, it is currently infeasible to
address with a formal model selection analysis — hence
a rationale for using our well-tested and highly developed models of protein evolution instead. The convergent
SELEX RNAs are certainly interesting and could in principle be analyzed in this framework, but they are less
directly relevant to the question of UCA because they
have not traditionally been used as an argument for
UCA, whereas the universal genetic code has.
The paper is generally well-written and, with the
caveats above, in my opinion suitable for publication
after revision. It might benefit from shortening, as some
of the points are overly belabored in the current presentation. A more concise discussion focusing on the main
ideas, i.e. the importance of model selection, the
assumptions of the Koonin & Wolf model, and the
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consequences of these assumptions in distinguishing
simulated and real data would likely increase readership
substantially relative to the present version.
Reviewer 2: Robert Beiko
(The review by Robert Beiko includes two consecutive
rounds of comments, here interleaved. The second
exchange is indented.)
In any event, the paper is certainly worthy of publication — I have some continuing problems with some
details that I outline below, but this is a great contribution to an ongoing discussion.
This paper is a detailed response to Koonin and Wolf
(ref [2]) in which a compositional model was used to
generate phylogeny-free sequences to test the model
selection framework of ref [1]. The paper consists of (1)
A justification of the need for a formal test of common
ancestry, (2) A detailed description of several critical
limitations of null hypothesis-based tests of statistical
significance, and (3) a detailed refutation of the work of
Koonin and Wolf.
I think part (1) is fine; I have not followed the genetic
code debate closely, but I agree that quantitative
hypothesis tests based on evidence apart from the
genetic code are worthwhile.
Part (2) addresses some well-covered areas of statistical theory, although the “Wolf vs. Koonin” etc. example
is less illuminating than the rest of the section. I think
e-values get short shrift, though: if one considers two
different e-values from two different comparisons, I
think one would be justified in taking the larger of the
two e-values to constitute greater evidence for a lack of
process generating similarity between the two sequences
(convergence, common ancestry, etc.).
Response: This is an exceedingly common misinterpretation of frequentist null-hypothesis significance tests. As
explained in the text, by the very logic of null-hypothesis
tests, a large E-value (or P-value) is evidence for nothing.
This cautionary point is routinely reiterated in introductory statistical texts, e.g. “Although a ‘significant’ departure provides some degree of evidence against a null
hypothesis, it is important to realize that a ‘nonsignificant’ departure does not provide positive evidence in
favour of that hypothesis. The situation is rather that we
have failed to find strong evidence against the null
hypothesis.” [123]. Similarly, “… a large significance level
indicates that, with respect to the particular test used,
the data provide no evidence that this hypothesis is false.
This should not be interpreted as evidence in support of
the hypothesis, but merely as a lack of evidence against
it. “ [124]
Here is one way of understanding why it is fallacious
to make conclusions from insignificant results. If the null
hypothesis is true, then we expect to find probable results
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from the null distribution (i.e., we expect a large “insignificant” E-value, e.g. E > 0.1). But using probable results
under the null to conclude that the null is true is committing the fallacy of affirming the consequent: if A then
B, we observe B, therefore A — an invalid syllogism. In
the case of sequence similarity tests, observing low similarity (e.g., a small S statistic in BLAST search) is
expected under the null distribution of random alignments. But we also expect low similarity if the sequences
are homologous and have diverged for a large amount of
time.
Given the lack of well-developed alternative models to
homology, it seems reasonable to me to consider a
small BLAST e-value as constituting stronger evidence
for homology than a larger one. I agree that this is not
as strong as explicit model comparisons, but it does
nonetheless highlight an important problem with the
entire procedure as reported in the 2010 Nature paper
and here.
Before I get to part (3), I have some major concerns
about the approach, in particular how the tests are formulated and how the results are interpreted as positive
evidence of common ancestry.
First and foremost, any likelihood or Bayesian modelcontrasting framework is only as good as the models
you feed to it.
Response: This is true, but from a Bayesian point of
view, this is not really a problem. Rather, it is a fundamental and inherent property of the scientific method
itself, common to all methods of inference in general,
and Bayesian methods handle it in the only proper way.
We never know the true model, and in fact we can be
certain that even our best models are wrong. To quote
Box: “all models are wrong, but some models are useful”
[125]. The purpose of a Bayesian analysis (and of science
in general, in my opinion) is this: given a set of models
hypothesized to explain our data, which model in this
set should we believe is best at explaining the data? The
most we can ever do is to say that one model is more
probable than another (and quantify how much more
probable).
The original 2010 paper contains the sentence “Statistically significant sequence similarity can arise from factors other than common ancestry, such as convergent
evolution due to selection, structural constraints on
sequence identity, mutation bias, chance, or artefact
manufacture”. But none of these alternatives is actually
tested alongside the hypothesis of common ancestry!
Response: I did indeed test some of those alternatives.
In my original 2010 Nature paper I explicitly tested
models of independent ancestry and chance convergence
of the observed sequence similarity (as well as the nested,
hierarchical patterns in the real protein data). Furthermore, my independent origin models are good
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approximations of independent origin models that
include convergence due to several of those other factors
(see below).
The independent origin tests use amino acid substitution models that were generated under the assumption
of homology, and apply them to sequences that are
completely homologous or very nearly so (see next paragraph). We seem to all be in agreement that these
sequences are homologous (indeed the author says so in
his response to Yonezawa and Hasegawa [116,120]:
“neither selection nor physical constraints alone can
plausibly generate the high levels of sequence similarity
(55% average sequence identity) observed in the universal protein data set that I used.”
Response: My quoted claim is not equivalent to conceding that the sequences are homologous. There are
other explanations, besides homology, for high sequence
similarity. My statement was not an assumption but a
conclusion based on my model selection results, taking
into account realistic biophysical and biochemical
considerations.
This statement taken in isolation is fine, but is at odds
with the claim that a meaningful, quantitative hypothesis
test has been formulated and carried out, since no
attempt has been made to develop plausible alternative
models (for instance, models with independent origins +
convergence) and let them fight it out with competing
alternatives.
Response: First, I did formulate and carry out a test
with alternative models — Figures 1b and 2b from the
original paper [1]are graphical representations of some
of these alternative, independent ancestry models. The
independent ancestry models that I considered could in
principle produce the observed protein data, but the
model selection tests show that the probability of chance
convergence from independent origins is extremely low.
Second, my response to Yonezawa and Hasegawa [120]
provides an explanation of why my independent ancestry
models are reasonable approximations to models explicitly incorporating convergence due to physical constraints and selection for function. Any independent
origin model incorporating selection and/or physical constraints must be based on the known biophysical and
biochemical properties of proteins. The most pertinent
characteristic of proteins is their extreme functional
redundancy. To a good first approximation, primary
sequence determines structure, and in turn structure
determines function. Yet many sequences give the same
structure, and many structures provide the same function
[120,126-128]. All our biophysical and biochemical data
indicate that the sequence space consistent with any particular function is so large as to be nearly indistinguishable from random background residue frequencies
[120,126-131]. For selection to converge on similar
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sequences, sequence space must be tightly coupled to
function space, so that independent selection pathways
for the same function would be likely to result in similar
sequences. In reality, however, there is an incredibly
large sequence space associated with any particular function — so large that knowledge of the function alone tells
us essentially nothing about the possible sequences that
could specify that function.
In accord with these biophysical facts, each independent ancestry in my models has a prior on the residue
frequencies given by their background frequencies (these
can be provided a priori by the residue substitution
matrices, but in my analyses they were actually inferred
from the protein sequence data). Hence my independent
ancestry models approximately account for (1) constraints on protein sequences imposed by function and
(2) the prior probability of selection for function converging on similar sequences. For the same reasons, the
independent ancestry models can also be considered as
representing design hypotheses in which a “designer”
intended to produce proteins with similar functions and/
or structures, with an ignorance prior on the sequence
space fulfilling those criteria (reflecting the fact that we
know nothing about the intentions of the designer). For
proteins with highly dissimilar sequences, it would be
important to carefully and explicitly account for the very
weak constraints on sequence imposed by function. But
the proteins in my universal data set have relatively high
sequence similarities. Hence the extremely large model
selection scores strongly suggest that these approximations are reasonable, since subtle differences in background frequencies will have a negligible effect on the
model selection scores reported in my Nature letter.
Beiko response:
The “universal” proteins do indeed have high
sequence similarities, but at the same time the ribosomal proteins you examined would seem to be an
extreme case in comparison with the enzymes that
were examined in e.g., [126]. The highly interacting
nature of ribosomal proteins, along with their tendency to co-localize in large operons, would potentially make the probability of convergence quite a bit
higher than for your typical garden-variety “active
sites + a bunch of glue” enzyme. I agree that a
proper model of independent origin of (at least
some) ribosomal proteins + convergence would not
be expected to tip the scales in terms of model evaluation, but the degree of model preference could
easily shrink by quite a bit.
Response: This is a good point — physical constraints, such as necessary physical interactions
between ribosomal proteins and the ribosome,
increase the probability of convergence (i.e.,
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increasing constraints decrease the size of the relevant sequence and structure space consistent with a
given function). For proteins with very weak similarities, these constraints may be important to model. In
any case, my results are robust to omission of the
ribosomal proteins.
I mention “completely homologous” because there is a
serious problem contained within at least some of the
supplementary examples of the 2010 paper. Consider for
instance the three sequences in Section 4.3, where E+M
have significant sequence similarity, as do M+P, but not
E+P. But looking at the BLAST alignments clearly
shows these sequences for what they are: M is a multidomain protein that is partially homologous with E and
partially homologous with P in a way that does not
overlap with E. But the alignment columns are then
shuffled, such that M+P are identical in columns
1,2,5,8,9, and so on, while E+M are identical at 3,4,6,7,
etc. Were these sites properly clustered, inspection of
the BLAST local alignments would immediately give a
clear indication of what is going on. But since the columns are shuffled (and I know of no process that would
give rise to this pattern of intercalated similarities),
BLAST is railroaded into showing both local alignments
as covering the entire protein length. This seems like an
irrelevant example when the highly conserved proteins
used in the main paper will show no such tendencies. I
would like to know how the example in 4.2 was generated as well.
Response: None of this matters for the intended point
— these sequences were not intended to mimic proteins
in my dataset, they were made to illustrate a methodological point. The point of the example in Section 4.3 is
simply that the model selection tests prefer independent
ancestry for certain highly similar sets of sequences
(sequences with extremely statistically significant similarity, E ⋘ 10-100). Therefore the methodology considers factors other than mere sequence similarity in assessing
independent vs common ancestry, contra Koonin and
Wolf.
The second problem is that the entire notion of common ancestry is ill-defined, especially in light of lateral
genetic transfer. I think it is unlikely in the extreme that
the components of the universal cellular machinery
examined here are anything but homologous, but it
seems to me that establishing common ancestry of each
of these components does not guarantee that there was
a single ancestral organism (or population of organisms,
for any reasonable definition of ‘population’) in which
all copies of the machinery were ancestral to the ones
we would see today, which would seem to be necessary
to make the leap from “common ancestry of a bunch of
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proteins” to “a common ancestor of life”. This matter
has been raised by Peter Gogarten, Olga Zhaxybayeva,
Ford Doolittle, and Joel Velasco (pers. commun.),
among others. What exactly is being formally tested
here?
Response: Universal common ancestry is defined here
as “the proposition that all extant life is genetically
related” [1]. The fundamental question I addressed was
not whether the universally conserved genes in the Brown
dataset are similar — they unquestionably are. Rather, I
tested whether these sequences — and by necessity the
organisms that carry them in their genomes — are
genetically related by common ancestry. If you carry
genes in your genome that are homologous to genes carried in the genomes of all other living organisms, then
logically you are genetically related to all other living
organisms. It is not simply that we have “common ancestry of a bunch of proteins”. Rather, we have “common
ancestry of a bunch of fundamental proteins that are
each found in all known living organisms”.
Lateral genetic transfer is an orthogonal question. All
life could be genetically related, via only vertical genetic
inheritance from ancestor to descendant. Alternatively,
all life could be genetically related, with rampant lateral
gene transfer. There are many intermediate possibilities.
The issue of the nature of the “universal common
ancestor” is also largely independent of the status of universal common ancestry. For instance, Ford Doolittle
speaks of common ancestry without a common ancestor.
It will be useful to quote him at length:
We (some of us) do doubt that there ever was a single universal common ancestor (a last universal common ancestor or LUCA), if by that is meant a single
cell whose genome harboured predecessors of all the
genes to be found in all the genomes of all cells alive
today. But this does not mean that life lacks ‘universal common ancestry’ — no more than the fact that
mitochondrial DNA and Y-chromosome phylogenies
do not trace back to a single conjugal couple named
Eve and Adam whose loins bore all the genes we
humans share today means that members of Homo
sapiens lack common ancestry. That ‘common ancestry’ does not entail a ‘common ancestor’ is perhaps a
subtle point … [15]
Similarly, I wrote in the original 2010 Nature letter:
UCA does not demand that the last universal common ancestor was a single organism, in accord with
the traditional evolutionary view that common
ancestors of species are groups, not individuals.
Rather, the last universal common ancestor may
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have comprised a population of organisms with different genotypes that lived in different places at different times.
The fact of the matter is that organisms existed in the
past that contained ancestral copies of these fundamental proteins, and that all known extant life has inherited
descendant versions of these proteins from these ancestral
organisms (at least that is the scenario that my model
selection tests strongly support). Whether you want to
call that ancestral group of organisms “a species”, “a
population”, “an ancestor”, “the LUCA”, or something
else is primarily an issue of semantics. My universal
common ancestry models are also consistent with a single individual organism/cell that contained all the ancestral versions of these proteins, though that is extremely
unlikely given basic pop-gen considerations (and even
less likely with LGT).
Because all extant living organisms carry descendants
of these fundamental proteins, at some point the ancestral group of organisms necessarily had the ability to
exchange fundamental genetic material. This is one
argument for calling this ancestral population a “species”, regardless of whether it was exchanging genetic
information via sex or LGT or whatever — e.g., that
would be a strict application of the Biological Species
Concept. Similarly, Doolittle and others have argued
that “the proper way to model prokaryotic evolution over
4 Gyr is as a single, albeit highly structured, recombining
population, not an asexual clade.” [15].
The rest of this review I dedicate to the Results and
Discussion, part (3) of the paper. 3a, 3b and 3c refer to
the three claims that are to be refuted (top of p. 15), 3a
is further split into four parts.
3a-I, pp. 15-17: Of course phylogeny of a group of
sequences models the hierarchical structure of a set of
sequences in a way that simple pairwise BLAST cannot.
But sequence similarity is evidently a major contributor
to the optimal tree in terms of its branch lengths and
topology, and based on the examples presented in the SI
of the original Nature paper, it seems that one could
use a graph-based approach to building putatively
homologous sequence sets from cliques or almost-cliques of BLAST results. To me, it seems that extending
the analysis of sequence similarity to sets (n > 2) of
sequences may be the critical factor in the model test,
rather than the following step of phylogenetic inference
and modelling. Can a counterexample be constructed
where most or all sequences in a set show statistically
significant similarity to one another, yet the likelihoodbased tests support independent ancestry over common
ancestry?
Response: Yes, and I presented exactly this type of
counter-example in Section 4.3 of the Supplementary
Page 19 of 25
Information of my original paper. I have also constructed
many other examples where three or four sequences all
have highly significant sequence similarity to each other
(rather than just two of three pairwise comparisons as in
Section 4.3). In response I now present an additional
four-sequence example in the text.
3a-II, p. 17: Similarly to above, I don’t think it’s fair to
say that the three proteins in the example in 4.3 of the
Nature paper show “significant similarity” when only
66% of the sequences show such similarity.
Response: Homology is transitive — if A and B are
homologous, and B and C are homologous, then A is
homologous to C. If significant sequence similarity is in
fact a reliable marker for homology, then those three proteins should be homologous even though only two of three
pairwise comparisons show significant sequence similarity. Analogous examples are commonly found in real
proteins. Regardless, the new four-sequence example
should mollify this concern.
Beiko response:
Homology is clearly not transitive in the case of
multidomain proteins. For example, if protein P1 has
domains X+Y and protein P2 has domains Y+Z, it is
not correct to say that a third protein P3 containing
only domain Z is homologous to P1 because P2 happens to contain elements of both P1 and P3.
And this is clearly what is happening in the threeand four-protein examples: careful inspection of the
proteins in Appendix 2, Additional File 1 shows that
each column either supports a perfect partitioning of
the sequence sets into BE+MP, or BM+EP, or BP
+ME. So this example is equivalent to taking six distinct, non-homologous domains, and building
sequences E = D1D3D5, M = D1D4D6, B =
D2D3D6, P = D2D4D5 with odd/even pairs forced
to sit on top of one another in an alignment. Shuffling the columns to generate the Appendix 2, Additional File 1 sequences allows BLAST to construct
local alignments that span non-homologous “gaps”
between the fragments of homologous domains, thus
making it seem like the sequences are similar to
each other in non-exclusive ways.
My point here is that these examples have similarity
patterns that are evolutionarily implausible,
Response: This is exactly the point. The patterns of
similarity in these artificial sequences are highly unlikely to have been generated by evolutionary, phylogenetic processes as described by the common ancestry
models. These patterns of similarity, however, could
easily result if the sequences have independent origins
(e.g., from some sort of convergent process or by
design — the latter independent origin hypothesis is
the correct one for these sequences). Whatever the
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case, the sequences are highly similar, and yet nevertheless the model selection tests (correctly) choose
independent ancestry over common ancestry.
and the argument that model comparisons capture
more than simple sequence similarity are not bolstered by these artificial scenarios. The manner in
which these examples were constructed could be
described as “partial common ancestry”, and raise
the question of what model should be preferred
when sequences are forcibly aligned in such a way
that part of the alignment is true homology and part
is not. The preference for BE+MP in Table 2 is presumably a consequence of more columns supporting
this pairing than any other.
The 4.2 example is more confusing to me as I do not
see how the likelihood is generated for the independent
origin model. Is it based solely on stationary amino acid
frequencies, without any branch lengths estimated? It
seems to me that an example with two sequences is not
ideal to illustrate the distinction between the two types
of approach: were a third sequence added that was similar to 1&2 such that all pairs of the triad were significantly similar, I presume that common ancestry would
once again be supported.
Response: I agree that the 4.2 example is less applicable, so I have removed reference to it in the text.
3a-III and IV, pp. 18-19: I do not think K&W suggested that the universal proteins could have been generated by a process lacking in phylogenetic structure:
Response: As I read it, K&W implied that their profile
model was a suitable model for the universal proteins, at
least as far as my model selection tests were concerned.
Otherwise, what is the relevance of their profile model to
the actual data analyzed in my paper?
rather, the point of their paper was that the key result
of CA > IA could be generated from a dataset in which
CA was not the correct model.
Response: As I argued in detail in the text, K&W have
never shown that their artificial dataset was not generated by a CA model.
It also seems odd to contrast a star tree model with
the partial independent origins model, when the natural
complement to a star tree would be an independent origin for each of the sequences considered. I expect under
those circumstances that the star tree would be favoured
over a true independent origins model, as is the case
with the K&W data.
Response: I also expect that a star-tree would be preferred over independent origins for each of the sequences,
but I don’t find that to be a very informative comparison. In contrast, the star-tree vs independent ancestry
tells us something important. Star-trees model similarity,
but not nested hierarchical patterns. The independent
Page 20 of 25
origin models do the opposite; they model hierarchical
patterns well, but not similarity between the independent
groups. The key observation is that star trees are worse
than independent origin models for the real proteins (as
gauged by the model selection scores). This strongly suggests, then, that hierarchical structure is more important
than similarity for the real protein data.
Beiko response:
What I was getting at here is that in the partial independent origins model, hierarchical structure and
similarity are still conflated at every level except that
of the deepest interdomain relationships. And I
would expect these relationships to have the smallest
overall impact on the question of hierarchy vs. similarity, since they would be the least stressed out
about having to coexist in a star tree, as opposed to
much more similar sequences that desperately want
to share an internal branch somewhere, anywhere. I
don’t think the distinction here is as clean as it is
made out to be.
Response: I agree the distinction is not completely
clean. Nevertheless, a hypothesis that can describe
some hierarchical structure, but absolutely no similarity between two groups ("partial” independent
ancestry), does much better than a hypothesis that
cannot model hierarchical structure, yet models similarity between the groups well (star tree). The independent ancestry hypothesis cannot account for any
similarity between the two groups, whereas the star
tree can, and yet the star tree, a common ancestry
model, does much worse. Therefore, something in the
independent ancestry hypothesis, something necessarily other than mere similarity, is responsible for the
independent ancestry hypothesis beating the star tree.
The only factor that could be responsible is hierarchical structure, and this is the case even though only
the deepest interdomain relationships are really
affected.
Concerning the profile model, it’s not surprising that
the model under which the data were generated turns
out to perform best. Clearly the K&W simulation was
not intended to mimic the structure of the universal
protein data set, but the fact remains that data sampled
under residue probability distributions, with no true
phylogenetic structure, generated a data set which led to
an incorrect preference for the model presented in the
original paper.
Response: As I explained in the text, if the data are
generated by a common ancestry model (as K&W’s profile model is), and the tests choose common ancestry,
then they chose correctly. And more importantly, when
the true generating model is included in the set of models
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being tested, the model selection tests choose the true
generating model.
Also, please clarify why the amino acid dataset has a
data-to-parameter ratio of 0.63.
Response: For the profile model, each column in the
alignment has 19 free parameters (the 20 residue frequencies that must be estimated, which sum to one). In
the real, universal protein data set, there are only 12
sequences, so each column has only 12 observations from
which to estimate the 19 parameters, giving a data-toparameter ratio of 12/19 = 0.63.
3b: Under “K&W’s justification is faulty”, two definitions of “independent” are conflated. What I take from
the K&W quotation is that the patterns of similarity at
each site are independent from one another, since there
is no underlying tree. Conversely, the common assumption of “independently evolving sites” does not require
that sites have uncorrelated histories or patterns of similarity, rather that changes at one site are not conditional
on changes at other sites.
Response: Admittedly the K&W quotation is somewhat
vague as to just what they mean by “independent”. However, it does not matter for my point if your interpretation is correct. Just because the patterns of similarity at
each site are independent from one another does not
mean that there is “no signal of common ancestry” or
“no evolutionary signal”, as K&W claim. As I mentioned
in the text, a star tree produces patterns of similarity at
each site that are independent from one another — and
a star tree is a bona fide phylogeny, being an evolutionary representation of common ancestry.
K&W themselves never claimed that their sequences
were artificially convergent, only that they are highly
similar.
Response: Three counter-examples from their comment: “these alignments contain no signal of common
ancestry (in more general terms, no evolutionary signal)
whatsoever … “. “Alignments of statistically similar but
phylogenetically unrelated sequences successfully mimic
the purported effect of common origin.” “The computational experiment on the estimation the likelihoods of
alignments of similar but evolutionarily unrelated
sequences.” Sequences that are similar yet evolutionarily
(or phylogenetically) unrelated are by definition convergent at the level of sequence [132].
While these sequences were indeed sampled from
homologous alignment columns, they certainly would
possess what I would consider to be “conflicting phylogenetic signal”. Indeed there seems to be some confusion about whether that term is meant to refer to
reticulate evolutionary patterns within a single set of
homologous genes, or the partial homology problem I
point out above.
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Response: By “phylogenetic signal”, I mean non-random, nested hierarchical patterns of similarities in the
sequences. It is possible for a single set of sequences to
have two or more very different, incompatible nested patterns of similarities, which is what I mean by “conflicting
phylogenetic signal”. This can occur in concatenated
alignments of homologous proteins when there is reticulate evolution (since each protein is treated as one single
long sequence). But it can also occur within a single protein (for instance reticulate evolution of domains in a
multi-domain protein), or within a single protein
domain. For my purposes the cause of conflicting phylogenetic signal is irrelevant — the point is that conflicting
phylogenetic signal is highly unlikely to result from a
common ancestry model (in which a local region of
sequence is modelled with a phylogenetic tree). Regardless, any apparent conflicting phylogenetic signal found
in K&W’s artificial data is necessarily only due to random chance.
The comparison of the sampling protocol of K&W to
the models of Bruno is very interesting, although the
fact that the generating columns had hierarchical structure to begin with makes me wonder whether the analogy is accurate or not. In any case, does this mean that
we cannot in fact distinguish homologous proteins from
nonhomologous proteins that exist in a reduced but
shared sequence space due to structural constraints?
Response: In some cases, I think the answer is yes.
However, imagine we have a reduced sequence space
and yet the actual sequences show strong nested, hierarchical patterns. In that case the common ancestry
models should explain the data better than independent
ancestry models (better than models that account for the
reduced sequence space yet cannot account for hierarchical patterns), and so we should be able to distinguish the
two.
3c: You should probably add the assumption that the
sequences used to generate the substitution models
(JTT, WAG, etc.) were themselves homologous, and
emphasize the assumption that the Markovian process is
stationary, reversible, and homogeneous.
Response: I’ve modified the text regarding the Markovian assumptions. But the substitution models deserve
some comment, and I have added a section of clarification in the text. First, for the formal purposes of the
model selection tests, we don’t actually know that the
substitution models (like WAG) were based on homologous sequences, and this assumption is unnecessary. The
only thing we really know is that the sequences used in
constructing WAG, etc. were similar. From a modelselection perspective, the origin of the substitution
matrices is irrelevant — the likelihood function doesn’t
know where the matrices came from, and the likelihood
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is the final judge. All that matters is that some substitution matrices give higher likelihoods than others.
Beiko response:
But the WAG matrix was built on the underlying
assumption that a phylogenetic tree related the
sequences whose changes contributed to the entries
in the matrix. If WAG was in fact forcing similar
but non-homologous sequences to obey a phylogenetic framework, wouldn’t that have some impact on
your contrasting of models that have varying components of phylogenetic relatedness?
Response: The WAG matrix is, ultimately, nothing
more than a proposed set of substitution rates.
Regardless of where those rates came from, they may
work well in the evolutionary models or they may not
(relative to other rate matrices). More importantly,
perhaps, is the fact that we can dispense with an
assumed rate matrix altogether and use Mr Bayes to
infer a general time reversible amino acid rate
matrix from the universal protein data itself. I have
done such with the universal proteins; it doesn’t
change the results. And the matrix inferred from the
actual data is qualitatively quite close to WAG.
These assumptions seem particularly relevant if we are
testing common ancestry of sequences that may have
initially emerged in a period of reduced amino acid
diversity and other drastic differences in evolutionary
processes. I’m not an expert on early amino acid alphabets, but it seems that contrasting CA vs. IA at a time
when there were 10 or fewer amino acids in use would
drastically change the degree to which different models
are preferred, especially if a meaningful model for convergence could be developed.
Response: These considerations are worth keeping in
mind. But since all of these proteins (from widely divergent taxa) have the same 20 amino acids and the same
genetic code, the most parsimonious explanation is that
the genetic code (and amino acid alphabet) was set in its
modern form well before the divergence of this set of proteins (however, Syvanen offers an alternative view that
arginine and tryptophan were added rather late [30]).
Reviewer 3: Michael Gilchrist
This paper is a response to a critique of the author’s
previous high profile paper in Nature [1]. Theobald
(2010) claimed to have quantitatively evaluate the
hypothesis that there is a single, universal common
ancestor for all of extant life. The author did this by
comparing the ability of alternative models to explain
the sequence similarity observed in a set of ‘universal’
proteins. The critique by Koonin and Wolf [2] argued
that Theobald’s “… demonstration of the universal
Page 22 of 25
common ancestry is a trivial consequence of significant
sequence similarity between the analyzed proteins.”
Koonin and Wolf go further to assert that the ability to
demonstrate universal common ancestry (UCA) “… is
unlikely to be feasible in principle.” Two of the
reviewer’s of this paper were also quite critical of the
Theobald paper, arguing its result is either based on circular reasoning or ‘trivial’ in nature.
In the current paper Theobald addresses these criticisms by arguing that they are either incorrect, in the
case of whether or not his model will be preferred by
model selection even if it is incorrect, or misleading, in
the fact that Koonin and Wolf’s data is simulated in a
manner consistent with common ancestry, but in a nonnested manner (i.e. a star tree). In the end I find Koonin
and Wolf’s ‘demonstration’ of Theobald’s approach to
be poorly thought out, failing in fact to demonstrate
what they claim, and Theobald’s response to be thoroughly convincing. (I guess this should not be unexpected if you can choose your reviewers). Further, I see
no philosophical reason why the UCA hypothesis cannot
be tested and find myself convinced that this is the best
explanation of the data given the set of models currently
being proposed.
In terms of criticisms, I find the author’s definitions of
P-values and E-values to be so similar that the reader is
left a bit confused about how they differ.
Response: P-values and E-values are indeed quite
similar, and in my experience most people find the subtle
difference between P-values and E-values to be confusing
and arcane. For the purpose of this paper the similarity
is the important thing — the difference does not matter,
as there is a one-to-one correspondence between P-values
and E-values, they have the same philosophical statistical justification, and they are used identically in nullhypothesis significance tests.
I think the author could improve the paper by revisiting the section where he states “Now imagine that you
replace these six sequences …” Stating that the likelihood will change if you change the data seems trivial
and, given how models are evaluated in terms of relative
differences in likelihood, confusing as to the main point.
Response: It may seem trivial to those familiar with
the likelihoods of probabilistic phylogenetic models. But
the point is important: it is possible to change the
sequence data so that the similarity is unchanged. If the
likelihood changes but the similarity does not, then the
phylogenetic models, and hence the model selection
scores, necessarily gauge something besides mere sequence
similarity, contra K&W.
In addition instead of saying “… the likelihood of a
phylogenetic tree is also a function of the particular patterns of characters … “ (particular patterns is a bit
vague) it might be better to say “… the likelihood of a
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phylogenetic tree is also a function of the nested nature
of the similarities in the data… “
Response: The sentence mentioned has been changed
as suggested.
Overall, I think that it is interesting to see the clash of
scientific philosophies on display between the ‘old
guard’ of Koonin and Wolf (and reviewers) whose scientific interpretation and training appears to be centred on
null hypotheses and the ‘new guard’ of Theobald whose
work is focused on model selection.
Additional material
Additional file 1: Appendix 1 and 2.
Acknowledgements
I thank Nicholas Matzke and Reed Cartwright for comments and criticism. I
thank the NIH for funding (GM094468 and GM096053)
Authors’ contributions
DLT carried out all work and wrote the manuscript.
Competing interests
The author declares that he has no competing interests.
Received: 22 July 2011 Accepted: 24 November 2011
Published: 24 November 2011
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doi:10.1186/1745-6150-6-60
Cite this article as: Theobald: On universal common ancestry, sequence
similarity, and phylogenetic structure: the sins of P-values and the
virtues of Bayesian evidence. Biology Direct 2011 6:60.
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